Evidence-Based Medicine in Uveitis

Scott M. Whitcup

Key concepts

•All published literature does not have equal   import.

•All medical literature, including this book, must be read critically.

•Whenever possible, treatment decisions should be based on evidence-based medicine. Evidence-based medicine is defined as the conscientious, explicit and judicious use of current best evidence in making decisions about the care of individual patients.

•The best evidence usually comes from well-  conducted, randomized clinical trials; however, there are relatively few randomized clinical trials in uveitis, although the number is increasing.

•It is important to understand the strength or level of evidence supporting treatment decisions.

The practice of medicine is based on applying what we have learned from our medical training in addition to the know­ ledge gained by reading books and articles and attending scientific conferences. It is our hope, for example, that the book you are reading will assist you in the care of patients with uveitis. However, all medical literature, including our book, must be read critically. Much of the information that appears to be irrefutable scientific dogma is actually based on inconclusive data derived from a handful of patients. Because the recommendations are in print and stated by seemingly reputable authorities, they are often followed blindly. It is frequently useful to thoroughly review the origi­ nal references on which various therapeutic approaches are based; what you find may surprise you.

There is a growing movement to basing treatment deci­ sions on evidence-based medicine. Evidence-based medicine is defined as the conscientious, explicit and judicious use of current best evidence in making decisions about the care of individual patients.1 Evidence-based medicine has been divided into two types: evidence-based guidelines and evidence-based individual decision making. In each case, the goal is to base therapy on the best evidence available. A number of classifications for the quality of evidence have been proposed. One commonly used stratification was developed by the US Preventative Services Task Force and is detailed in Table 6-1). An assessment of the quality of the information in the literature is critical in determining the best treatment for our patients.

When treatment recommendations are made in pub­ lished guidelines or in the literature, they can also be catego­ rized by the level of evidence on which the information is based. The US Preventative Services Task Force uses the categories listed in Table 6-2.

When you read the medical literature, it is important to determine the experimental methods used in the various studies. Sometimes this information can be discerned from the title of the paper; at other times the Methods section must be read. Occasionally the study method is not stated in the paper: if this is the case, the article is probably not worth reading. Many of the clinical studies in the literature are retrospective, meaning that the data were collected from previous patient visits. Retrospective studies can provide valuable information but are usually limited by the quality and thoroughness of the patient records. A patient’s symp­ toms and clinical findings, although present, are often not recorded. For example, if there is no comment in a patient’s record about vitreous haze, does this mean that vitreous haze was absent or that it was present but not recorded in the note? Fortunately, most ophthalmic notes contain a core of data including visual acuity, intraocular pressure, and results of anterior segment and retinal examination. Never­ theless, prospective studies, when specific data are collected during patient visits on specifically designed case report forms, are less prone to errors.

Study design

There are four basic clinical studies: case series, case–control studies, cohort studies, and randomized clinical trials.2 The case report or case series is probably the weakest method of deriving clinical data. Case series are usually retrospective reviews that list the clinical findings of patients with a spe­ cific disease. Case series can illustrate the variety of clinical manifestations of diseases and provide information about diagnosis, management, and prognosis. However, in addi­ tion to the problem of data missing from patient records, the reader should be aware of other pitfalls that may jeop­ ardize the value of the report. First, the disease or condition may not be adequately defined. If patients with sympathetic ophthalmia are inadvertently included in a series of patients with Vogt–Koyanagi–Harada syndrome, the findings and conclusions may be altered. Second, the patient population reported may be dissimilar from that in the clinician’s prac­ tice. Frequently uveitis specialists see patients with more severe diseases because these are the ones referred to their practice. Therefore, a uveitis specialist may report that the

Table 6-1  US Preventative Services Task Force classification for the quality of scientific information in the literature

Level I Evidence obtained from at least one properly designed randomized controlled trial

Level II-1 Evidence obtained from well-designed controlled trials without randomization

Level II-2 Evidence obtained from well-designed cohort or casecontrol analytic studies, preferably from more than one center or research group

Level II-3 Evidence obtained from multiple time series with or without the intervention. Dramatic results in uncontrolled trials might also be regarded as this type of evidence

Level III Opinions of respected authorities, based on clinical experience, descriptive studies, or reports of expert committees

Table 6-2  US Preventative Services Task Force classification for treatment recommendations

Level A Good scientific evidence suggests that the benefits of the clinical service substantially outweighs the potential risks. Clinicians should discuss the service with eligible patients

Level B At least fair scientific evidence suggests that the benefits of the clinical service outweighs the potential risks. Clinicians should discuss the service with eligible patients

Level C At least fair scientific evidence suggests that there are benefits provided by the clinical service, but the balance between benefits and risks are too close for making general recommendations. Clinicians need not offer it unless there are individual considerations

Level D At least fair scientific evidence suggests that the risks of the clinical service outweigh potential benefits. Clinicians should not routinely offer the service to asymptomatic patients

Level I Scientific evidence is lacking, of poor quality, or conflicting, such that the risk versus benefit balance cannot be assessed. Clinicians should help patients understand the uncertainty surrounding the clinical service

visual prognosis for a given disease, such as sarcoidosis, is poor. If this report is based on a series of patients composed of referred patients with end-stage disease, it may be biased. Be especially wary of retrospective reviews that make global dogmatic statements on the basis of a few patients. Finally, case series have no control group for comparison. If a report states that depression was found in 35% of patients with uveitis, it is not clear that this represents a causal relation­ ship. Visual loss and not uveitis may be the cause of depres­ sion. It would be important to know how many patients with other ocular diseases that cause visual loss (a control group) have depression. For example, the same percentage of patients with visual loss from retinal degenerations may also be depressed.

The case–control study is a second type of clinical study in which the investigator compares a group of patients with a given condition to a control group without the condition. The records of both groups are then compared to see whether certain factors were more likely to occur in one group than in the other. The classic example of a case–control study would be to examine patients with lung cancer and a group without the disease and determine their smoking history. It

Study design

is then possible to compute an odds ratio that determines the relative risk for a given condition such as lung cancer, given a specific factor such as smoking. Case–control studies, albeit more powerful than case series, are prone to bias, many relying on a retrospective review of patients’ records to determine the differences in a number of clinical param­ eters between cases and controls. Additional bias arises from the method of choosing the case and control subjects. Despite the potential bias, case–control studies are becom­ ing more common in the literature because they are easy to carry out, especially with the computerization of clinical records. In addition, they are often the only feasible method available to study rare disorders.

A cohort study identifies two groups or ‘cohorts’ of patients, for example one cohort that receives a certain treatment and one cohort that does not. The groups are then followed prospectively for the development of a specific outcome. However, because the treatments are not assigned randomly, it is possible that the two groups differ in important param­ eters. For example, if you followed two groups of patients with glaucoma, one treated with medications and one treated surgically, you may falsely conclude that surgical therapy is inferior for treating glaucoma because these patients had a worse visual outcome. However, it may be that the patients treated medically had milder disease and better initial visual acuity than patients who received surgical therapy.

Pharmaceutical drug development includes a number of clinical studies, but the final determination of safety and efficacy is based predominantly on pivotal randomized, con­ trolled clinical trials. Clinical studies during the development of a new medication are divided into four phases. Phase I clinical trials are the initial safety trials of a new medicine and are usually conducted in normal volunteers. The trials can be open label, for which patients and investigators are unmasked to the treatment allocation. Multiple doses may be tested in a phase I trial, often starting with the lowest dosage and esca­ lating to higher dosages if tolerated. Phase II trials are designed to study the safety and efficacy of a new medication. These trials are often double-masked, in which neither patients nor investigators know what treatment is being administered. Classically these are called double-blind studies; however, in ophthalmology we prefer the term double-masked, because it is difficult to get a patient with an eye disease to enroll in a study with double-blind in the title. Phase II trials typically have more patients than phase I trials and are conducted in patients with the disease, but still may examine several dosages or treatment regimens. The phase III clinical trial is the pivotal clinical trial for the approval of the medication. These are almost always larger randomized clinical trials comparing the new medication to the standard treatment or to placebo. The US Food and Drug Administration (FDA) almost always requires two phase III trials with corroborative findings before approving a new drug. Studies conducted after a medicine is approved and marketed are called phase IV trials. These are conducted in patient populations for which the medicine is intended, and may compare the medi­ cine to currently available therapies.

The randomized clinical trial provides the most powerful evidence about the value of a new therapy or diagnostic approach.3 Because patients enrolled into the study are ran­ domly assigned into a specific group, if there are sufficient numbers of patients the groups are usually equivalent

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Part 2 • Diagnosis

Chapter 6 Evidence-Based Medicine in Uveitis

Box 6-1  Components of a randomized clinical trial

•Study approved by Institutional Review Board (IRB) and appropriate informed consent obtained from patients

•Disease well defined with specific diagnostic criteria

•Patient population well defined with specific inclusion and exclusion criteria

•Patients randomly assigned to new treatment and control treatment according to standardized and documented procedures

•Patients and investigators appropriately masked from treatment assignment

•Sample size accurately determined to control for type I and type II errors

•Outcome measures specified, and minimum differences to be considered as clinically important, detailed

•Procedures for the conduct of the trial well detailed

•Timing of study visits and collection of data strictly specified and monitored

•Statistical analysis plan specified before locking of the database and unmasking of treatment assignments. Results of an intent to treat analysis, in which all randomly assigned patients are included in the analysis provided, even if additional analyses performed

clinically. From an ethical standpoint, randomized clinical trials should compare treatments when the investigator is unsure which therapy is better. The situation where both treatment approaches have equivalent merits is termed clini­ cal equipoise.4,5

Even randomized controlled trials need to be designed appropriately and well conducted to ensure meaningful results. Key issues in the design and conduct of randomized clinical trials are listed in Box 6-1. The investigators should have performed previous studies in the area and include people with appropriate training in the conduct and analysis of the study. The primary outcome of the study should be clearly stated, even if multiple outcomes are examined. The procedure for enrolling patients should be clearly delineated and state the inclusion and exclusion criteria. In addition, the therapy should be clearly stated, and the control group should be clinically appropriate. For example, if one were designing a trial to study the benefits of phacoemulsification as a technique for cataract surgery, it would be clinically inappropriate to compare this technique to intracapsular cataract extraction because extracapsular cataract surgery is the more frequently performed procedure.

It is extremely important that the paper include a discus­ sion of sample size calculation. Sample size is based not only on the event rate expected in the two groups but also on the level of protection against type I and type II errors. A type I error occurs when the study falsely concludes that the thera­ pies tested are different when in fact they are the same. A type II error occurs when the study falsely concludes that there is no difference between the therapies when in fact a difference exists. Many randomized clinical trials in the lit­ erature are underpowered. This means that the potential for a type II error is high: sometimes 30% or higher. In these studies a conclusion that there was no statistically significant difference between the two groups is meaningless: there could in fact be a big difference between the two groups, but not enough patients were tested to show that difference.

Here is an example of an underpowered study. If we wanted to test the hypothesis that the two sides of a quarter are dif­ ferent, we could flip the coin a number of times and record the results. If you flipped the coin three times (similar to enrolling three patients) and got heads each time, you might falsely conclude that the two sides were the same: both sides had a head on. The chance that you would reach this wrong conclusion would, however, diminish as you increased the number of times you flipped the coin! You would then have more power to show a difference between the two sides of the coin and thus have more protection against a type II error. Remember that studies can never definitively prove that two treatments are the same. No matter how many times you flip a coin and only see heads, there is still some chance that there was a tail on the other side that did not come up. Nevertheless, if you flip the coin enough times or enroll enough patients in a trial, the chance of this type II error becomes increasingly unlikely.

The data in randomized trials should be appropriately collected, and patients should have a reasonably high level of adherence to protocol procedures with few missed data or loss to follow-up. Observers should be masked to the treatments that patients receive. Statistical methods should be appropriate for the data and the tables and figures easily read. Finally, it is important that the authors’ conclusions are supported by the data and do not exceed the evidence. There are many examples in the literature where results in a narrowly defined patient population are inappropriately generalized to broader patient groups.

Clinical trials in uveitis

Unfortunately, most of the uveitis literature is composed of case series and case reports. As stated above, these studies can provide useful information but are highly prone to bias and lack a control population for comparison of the find­ ings. Despite their superior strength as a clinical design, few case–control studies or cohort studies of patients with uveitis have been conducted. Even rarer are randomized controlled clinical trials of therapies for patients with uveitis.6 Most of the published randomized clinical trials in uveitis focus on postoperative inflammation. Comparatively few randomized trials have studied therapies for other forms of uveitis. Part of the explanation for this stems from difficulties that arise when patients with this disorder are studied. Many forms of uveitis are rare; therefore, it is difficult to recruit enough patients to fulfill the sample size requirements. It is impor­ tant that the observers are masked to the therapy, which may be difficult if surgical treatment is compared with medica­ tions. Patients with uveitis often have underlying systemic diseases that make it difficult for them to follow a predeter­ mined therapeutic protocol because their other diseases often require systemic therapy.

Nevertheless, randomized clinical trials can be conducted in patients with uveitis. In these trials it is important to collect data in a standardized fashion. We record visual acuity according to a standard protocol with the use of ETDRS charts.7 Inflammatory activity is similarly recorded with standardized methods, such as grading scales for vitre­ ous haze or laser interferometry for anterior chamber haze.8 Well-conducted randomized clinical trials are not only

important in illustrating the safety and efficacy of new treat­ ments, but also in better defining the natural history of the disease. We will undoubtedly learn more about the underly­ ing natural history of inflammatory eye disease through the analysis of data from randomized studies.

Many large randomized clinical trials are conducted as part of the drug approval process. Unfortunately, few medi­ cations have been developed specifically for the treatment of uveitis. As a result, most of the therapies administered in clinical practice are used off label. More recently, there has been an interest in obtaining regulatory approval of medica­ tions for nonsurgical and noninfectious uveitis, and this has led to larger, randomized clinical trials. Sustained-release fluocinolone acetonide implants were shown to significantly reduce uveitis recurrences in patients with noninfectious posterior uveitis.9 Additional randomized clinical trials assessing several new therapies for intermediate and poste­ rior uveitis are currently in progress, and publications of these studies should follow and add to our understanding of the disease.

The National Eye Institute has conducted several small randomized clinical trials in patients with uveitis. In one study, ciclosporin was compared with prednisolone for the treatment of endogenous uveitis.10 In this trial, 28 patients were randomly assigned to treatment with ciclosporin and 28 were randomly assigned to treatment with prednisolone. Although no statistically significant difference was found between the primary outcomes of visual acuity or vitreous haze of patients in the two groups, because of the small numbers it would be wrong to conclude that the two thera­ pies were the same. The authors were careful not to state that the study proved that the two therapies were equivalent, and instead suggested that because similar outcomes were achieved, ciclosporin could be considered as an alternative to corticosteroid therapy. Because the randomized clinical trial is often the best source of useful clinical information, some of the randomized clinical trials on uveitis or other inflammatory eye diseases sponsored by the National Insti­ tutes of Health are listed in Box 6-2. Many important rand­ omized clinical trials have also been conducted on the ocular complications of AIDS, and these trials are described in Chapter 11.

References

Box 6-2  Examples of National Institutes of Health

– funded randomized clinical trials in inflammatory eye diseases

1.Argon laser photocoagulation for ocular histoplasmosis. Results of a randomized clinical trial. Arch Ophthalmol 1983; 101: 1347–57.

2.Endophthalmitis Vitrectomy Study Group. Results of the Endophthalmitis Vitrectomy Study. A randomized trial of immediate vitrectomy and of intravenous antibiotics for the treatment of postoperative bacterial endophthalmitis. Arch Ophthalmol 1995; 113: 1479–96.

3.Wilhelmus KR, Gee L, Jauck WW, et al. for the Herpetic Eye Disease Study Group. Herpetic Eye Disease Study (HEDS). A controlled trial of topical corticosteroids for herpes simplex stromal keratitis. Ophthalmology 1994; 101: 1883–96.

4.Herpetic Eye Disease Study Group. A controlled trial of oral acyclovir for iridocyclitis caused by herpes simplex virus. Arch Ophthalmol 1996; 114: 1065–72.

5.Nussenblatt RB, Gery I, Weiner HL, et al. Treatment of uveitis by oral administration of retinal antigens. Results of phase I/II randomized masked trial. Am J Ophthalmol 1997; 123: 583–92.

6.Nussenblatt RB, Palestine AG, Chan CC, et al. Randomized, double-masked study of ciclosporin compared to prednisolone in the treatment of endogenous uveitis. Am J Ophthalmol 1991; 112: 138–46.

7.Whitcup SM, Csaky KG, Podgor MJ, et al. A randomized, masked, cross-over trial of acetazolamide for cystoid macular edema in patients with uveitis. Ophthalmology 1996; 103: 1054–63.

8.Beck RW, Cleary PA, Anderson MM Jr, et al. for the Optic Neuritis Study Group. A randomized, controlled trial of corticosteroids in the treatment of acute optic neuritis.   N Engl J Med 1992; 326: 581–8.

9.Buggage RR, Levy-Clarke G, Sen HN, et al. A double-masked, randomized study to investigate the safety and efficacy of daclizumab to treat the ocular complications related to Behçet’s disease. Ocul Immunol Inflamm 2007; 15: 63–70.

10.Smith JA, Thompson DJ, Whitcup SM, et al. A randomized, placebo-controlled, double-masked clinical trial of etanercept for the treatment of uveitis associated with juvenile idiopathic arthritis. Arthritis Rheum 2005; 53: 18–23.

1.Sackett DL, Rosenberg WM, Gray JA, et al. Evidence based medicine: what it is and what it isn’t. Br Med J 1996; 312: 71–72.

2.Sackett DL, Haynes RB, Tugwell P. Clinical epidemiology: a basic science for clinical medicine. Boston: Little, Brown, 1985; 224–229.

3.Meinert CL, Tonascia S. Clinical trials design, conduct, and analysis. New York: Oxford University Press, 1986; 274–275.

4.Freedman B. Equipoise and the ethics of clinical research. N Engl J Med 1987; 317: 141–145.

5.Johnson N, Lilford RJ, Brazier W. At what level of collective equipoise does

a clinical trial become ethical? J Med Ethics 1991; 17: 30–34.

6.Okada AA. Noninfectious uveitis: a scarcity of randomized clinical trials. Arch Ophthalmol 2005; 123: 682– 683.

7.Ferris FL III, Kassoff A, Bresnick GH, et al. New visual acuity charts for clinical research. Am J Ophthalmol 1982; 94: 91–96.

8.Nussenblatt RB, Palestine AG, Chan CC, et al. Standardization of vitreal inflammatory activity in intermediate and posterior uveitis. Ophthalmology 1985; 92: 467–471.

9.Jaffe GJ, Martin D, Callanan D, et al. Fluocinolone Acetonide Uveitis Study

Group. Fluocinolone acetonide implant (Retisert) for noninfectious posterior uveitis: thirty-four-week results of a multicenter randomized clinical study. Ophthalmology 2006;

113: 1020–1027.

10.Nussenblatt RB, Palestine AG, Chan CC, et al. Randomized, double-masked study of cyclosporine compared to prednisolone in the treatment of endogenous uveitis. Am J Ophthalmol 1991; 112: 138–146.